Collider scope: when selection bias can substantially influence observed associations

1. Citation

Munafò MR, Tilling K, Taylor AE, Evans DM, Davey Smith G. “Collider scope: when selection bias can substantially influence observed associations.” International Journal of Epidemiology 2018;47(1):226–235. DOI 10.1093/ije/dyx206. PMID 29040562; PMCID PMC5837306. Published online 2017 Sep 27; issue date 2018 Feb.

Open access via PMC: https://pmc.ncbi.nlm.nih.gov/articles/PMC5837306/. Accessed 2026-07-13.

License / quoting posture. The article carries an explicit statement: ”© The Author 2017. Published by Oxford University Press on behalf of the International Epidemiological Association… This is an Open Access article distributed under the terms of the Creative Commons Attribution License (http://creativecommons.org/licenses/by/4.0/), which permits unrestricted reuse, distribution, and reproduction in any medium, provided the original work is properly cited.” CC-BY-4.0 → license-aware mode: short verbatim load-bearing quotes are reproduced below, each marked and located, with attribution to the citation above.

2. Access note

Full text of the article body read from the PMC deposit (title, abstract, Introduction, Boxes 1–3, “Collider bias”, “Simulations”, Tables 1–3, “Conclusions”, figure captions, references). No paywall boundary.

Boundaries of what was read:

• Figures 1, 2 and 3 are images. I read only their captions. The arrow directions in the DAGs of Figure 2 and of Figure 3 panels A–F are drawn in the images and are not recoverable from the text; where I state a structure below it is reconstructed from the prose + caption, and I say so. Figure 3’s six panels in particular cannot be redrawn from what I could read (see §11).
• The Supplementary Material (Supplementary Data, .docx, 86.2 KB) was not retrieved. It is cited for the composition of the smoking genetic risk score used in Table 3.

3. Thesis (1 sentence)

Selection into (or attrition from) a study is a form of conditioning on a collider, and therefore — contrary to the common assumption that unrepresentativeness harms only prevalence estimates and not associations — even modest selection effects can produce substantially biased and misleading estimates of phenotypic and genotypic associations.

4. Problem & context

• Large cross-sectional and cohort studies (UK Biobank, ALSPAC) are the workhorses of genetic epidemiology because small common-variant effects need very large samples.
• Participants who volunteer may not represent the “intended study population”; cohorts also lose representativeness through non-random attrition; and sub-sets selected for extra work (e.g. genotyping) are selected again.
• There is direct empirical evidence of selection in such studies: higher schizophrenia genetic risk scores are “consistently associated with non-completion of questionnaires by study mothers and children, as well as non-attendance at data collection clinics” in ALSPAC (Introduction, citing ref. 3).
• A literature (refs 5–9) argues representativeness is not necessary; refs 8 in particular is cited for the assumption the paper attacks. The paper’s own authors had previously argued the impact of selection bias on genetic associations would be modest, because conventional confounding is low for single genetic variants (refs 10, 12). The paper explicitly revisits and revises that prior position, motivated by (a) growth of highly selected samples like UK Biobank and (b) the shift from single variants to polygenic/allele scores.

The framing is stated in the abstract: the representativeness of these samples may be limited “either through selection into studies, or by attrition from studies over time,” and the paper explores this “from the perspective that this amounts to conditioning on a collider (i.e. a form of collider bias).”

5. Method / approach

Three strands:

(a) Conceptual/graphical. State collider bias (Figure 1: the coin-and-bell illustration; Figure 2: the simulation DAG; Figure 3: six selection scenarios A–F).

(b) Simulation. Data simulated on an allele score, a phenotype (P), and an outcome (O), where both P and O influence selection into the study, and there is no association between allele score and outcome in the intended study population.

Exact parameters as stated:

• All variables Normally distributed, SD = 1.
• Intended study population N = 9 000 000; baseline risk of selection controlled to yield a selected sample of approximately 500 000 (i.e. loosely modelled on UK Biobank’s ~5% response).
• P and O assumed to have independent effects (no interaction on the additive scale) on the odds of selection; effects set equal to each other for convenience.
• Selection effect sizes examined: OR = 1.2 (weak), OR = 1.5, OR = 1.8 — odds of missingness per 1 SD increase in phenotype/outcome. These correspond to a difference in mean phenotype/outcome of 0.2 SD, 0.4 SD and 0.6 SD respectively between participants and non-participants. The paper anchors 1.2–1.8 as “similar to estimates of the likelihood of participation in UK Biobank for individuals with any educational or vocational qualifications and for non-smokers” (see Box 2: OR 1.63 for qualifications, OR 1.90 for non-smoking).
• Allele score ↔ phenotype correlation varied: r = 0.05, 0.10, 0.15, 0.20, 0.30, i.e. genetic instruments explaining 0.25%, 1.00%, 2.25%, 4.00%, 9.00% of phenotypic variance. Anchored to reality: rs16969968 ≈ 1% of variance in cigarette consumption (ref 17); polygenic score for height ≈ 9% (ref 18).
• Analysis = unadjusted regression of outcome on allele score (NOT adjusting for the phenotype).
• 100 simulations per scenario.
• Two settings: no causal effect of P on O (Table 1) and a causal effect of P on O with regression coefficient 0.1 (Table 2).
• Note on why imputation is not the remedy here: selection into the study means all data on non-selected individuals are missing, and imputation “requires some data on which to base the imputation” (ref 16).

(c) Real-data example. ALSPAC (birth cohort, 14 541 pregnancies, ~75% of eligible women, expected delivery 1 Apr 1991 – 31 Dec 1992) vs ARIES, a sub-study of ALSPAC in which 1018 mother–offspring pairs were selected on availability of DNA at two time points for the mother and three for the offspring (ref 2). Compare the association between a smoking genetic risk score (variants at P < 0.05 in the Tobacco and Genetics Consortium GWAS) and maternal education (degree vs no degree) in the full cohort vs the selected sub-study (Table 3).

6. Key claims / findings

Mechanism

• Collider bias defined by common effect. Collider bias occurs when two variables X and Y independently cause a third variable Z. Z is then a collider, and statistical adjustment for Z biases the estimated causal association of X (exposure) on Y (outcome) (Figure 2).
• Adjustment ≡ selection. “Statistical adjustment of the XY association for a variable Z is equivalent to observing this association in a sub-population where all individuals share the same value of Z” (refs 1, 13). This is the identity that lets the paper move from adjustment language to selection language: if both X and Y cause participation Z, analysing the selected sample (Z = 1) is conditioning on Z.
• Bias has no fixed direction. “This bias can be towards or away from any true association, and can distort a true association or a true lack of association.” So collider bias can (i) create a spurious association where none exists, (ii) inflate, (iii) attenuate, or (iv) flip a real one.
• The bias propagates to genetic ancestors of the selecting phenotypes. If Gx → X and Gy → Y and both X and Y influence participation, then in the selected sample Gx will appear associated with Y — “unless X is also controlled for.” This is the paper’s stated route by which selection on phenotypes contaminates genotype–outcome associations.
• Indirect selection also suffices. Collider bias can arise even when the outcome Y does not directly cause selection, if Y is “a downstream consequence of something else that is causing selection into the study.”
• Polygenic scores are the highest-risk case. Because a polygenic score aggregates many variants associated with a phenotype, and the phenotype is associated with participation, the score is more strongly related to participation than any single variant is — so studies using polygenic scores, genome-wide allelic scores (ref 20), and whole-genome genetic correlations (refs 21, 22) are “most at risk of producing biased and potentially misleading results” when the sample is unrepresentative and the selection mechanism is unknown.
• Case-control secondary phenotypes are the same bug. Case-control studies condition on case/control status; if both genotype and a secondary phenotype associate with case-control status, the genotype–secondary-phenotype association is collider-biased (refs 29, 30).

Magnitude — simulation, null true association (Table 1)

Association of interest: allele score → outcome; true value = 0. Each row = 100 simulations. “Number of 95% CIs containing zero” out of 100 is the coverage; 95 would be nominal.

Paper’s own reading of this table:

• Bias is strongest for stronger independent selection effects and where the allele score is more strongly associated with the phenotype. (Both parameters matter; the induced association is monotone increasing in each.)
• Headline sentence: “even for moderate associations between missingness and both phenotype and outcome (OR = 1.5 for both phenotype and outcome) and between allele score and phenotype (r = 0.1, 1% variance explained by allele score) the confidence intervals contain zero only 89% of the time” — i.e. 11% false-positive rate at a nominal 5%, in a scenario the paper considers ordinary.
• At OR = 1.8 with r ≥ 0.20 the induced null association is detected as “significant” in 100 out of 100 simulations (0 CIs contain zero); mean z reaches −6.18 at r = 0.30.
• The bias is directionally negative in this parameterization (spurious inverse association), and the induced coefficients are small in absolute terms (−0.0002 to −0.008) — but at N ≈ 500 000 the standard error is small enough that small biases become highly significant. That is why the paper reports z-scores and CI coverage rather than only effect sizes.

Magnitude — simulation, non-null true association (Table 2)

Same design plus a causal effect of P on O (regression coefficient 0.1). Column “true regression coefficient” is the true allele-score→outcome effect (= 0.1 × r, i.e. transmitted through P).

Paper’s own reading: “Where there is a causal effect of P on O, the results are broadly similar, except that on the whole the confidence intervals had lower coverage than for the equivalent situation with no causal association.” (Note in the table the estimates are attenuated toward zero relative to the true value under strong selection — e.g. OR = 1.8, r = 0.30: estimated 0.020 vs true 0.030, with 0/100 CIs covering the truth. So here collider bias attenuates a real effect rather than manufacturing one.)

Magnitude — real data (Table 3, ALSPAC vs ARIES)

Selection into ARIES is itself associated with the relevant variables:

• Smoking (ever vs never) → being in ARIES: N = 13 249, OR 0.59 (0.52–0.68), P < 0.001 (smokers less likely to be in the sub-study).
• Smoking genetic risk score → being in ARIES: N = 7837, OR 1.00 (0.93–1.07), P = 0.92 (the score does not predict selection directly).
• Maternal education (degree vs no degree) → being in ARIES: N = 12 493, OR 1.86 (1.58–2.19), P < 0.001.
• Sanity check that the score works: smoking genetic risk score → ever smoking in ALSPAC: N = 7291, OR 1.07 (1.02–1.12), P = 0.003 (per SD of score).

The result:

I.e. the smoking genetic risk score is null against maternal education in the full ALSPAC cohort but significantly associated in the selected ARIES sub-sample — the induced association predicted by the collider mechanism, in real data, at N < 1000.

Empirical evidence of selection (Boxes 1 and 2 — the “is this real?” numbers)

Box 1 (ALSPAC):

• BMI vs retention, mothers: N = 11 319, OR 0.85 (0.81–0.88) per SD increase in pre-pregnancy BMI, for retention 2008–2011.
• BMI vs retention, offspring: N = 7954, OR 0.91 (0.87–0.96), retention at age 18 using BMI at age 7.
• Smoking heaviness vs retention among smoking mothers: N = 3534, OR 0.97 (0.96–0.98) per additional cigarette/day just prior to pregnancy.
• Consequence stated: if low BMI and maternal non-smoking both drive continued participation, the BMI–smoking association in ALSPAC will be negatively biased relative to the intended study population.

Box 2 (UK Biobank):

• Recruited >500 000 individuals aged 40–69, 2006–2010, from within 25 miles of 22 assessment centres, identified from NHS patient registers.
• ~9 000 000 invited; ~500 000 recruited → a 5% response rate (personal communication, UK Biobank, 8 July 2016).
• Current smokers: 19% general population vs 11% UK Biobank → equivalent OR 1.90.
• No qualifications: 25% vs 17% → equivalent OR 1.63.
• 5-year mortality far lower in UK Biobank than the UK population (ref 40).
• Consequence stated: if non-smoking and having qualifications both cause participation, the smoking–qualifications association in UK Biobank will be positively biased.
• Extra hazard: the first release of UK Biobank genome-wide data used two genotyping arrays, one applied to a nested case-control study of smoking and lung function (UK BiLEVE, ref 41), so the first-release genetic data are further selected relative to UK Biobank as a whole (stated to be resolved with the full release).

Real associations the paper says could plausibly be artefacts

The simulated bias magnitudes are “comparable to many reported associations derived from large but selected samples”, naming: personality ↔ cognitive function and a range of physical/mental health outcomes (refs 23, 24); chronotype (“morningness”) ↔ years of education (ref 25). Also offered as a possible resolution of a paradox: schizophrenia polygenic scores that maximally capture liability associate with increased psychotic experiences in ALSPAC, while more stringent variant-inclusion thresholds associate with reduced psychotic experiences (ref 27) — consistent with differential missingness rather than biology. Likewise, age-dependent differences in genetic correlations between cognitive ability and psychiatric disorders (ref 26) may be “an artefact of different selection bias pressures at different ages” rather than age-dependent pleiotropy.

7. Load-bearing statements — VERBATIM (license-aware mode; CC-BY-4.0)

All quotes verbatim from Munafò et al. 2018, IJE 47(1):226–235 (CC-BY-4.0), locations given.

1. Collider definition + the adjustment-induces-bias statement (section “Collider bias”, ¶3):

   “Collider bias occurs when two variables (X and Y) independently cause a third variable (Z). In this situation Z is a collider, and statistical adjustment for Z will bias the estimated causal association of X (exposure) on Y (outcome) (see Figure 2). Statistical adjustment of the XY association for a variable Z is equivalent to observing this association in a sub-population where all individuals share the same value of Z. Hence if both X and Y cause participation in a study (Z), then investigating associations in the selected sample (i.e. with Z = 1, indicating participation in the study) is equivalent to conditioning on Z, which in turn may induce collider bias.”

2. The abstract’s compact statement of the mechanism (Abstract):

   “We argue that because selection can induce collider bias (which occurs when two variables independently influence a third variable, and that third variable is conditioned upon), selection can lead to substantially biased estimates of associations.”

3. Direction of bias is unconstrained (section “Collider bias”, ¶1):

   “This bias can be towards or away from any true association, and can distort a true association or a true lack of association.”

4. Propagation to genetic proxies, and the one control statement the paper makes (section “Collider bias”, ¶4):

   “Therefore if genes Gx and Gy cause X (exposure) and Y (outcome), respectively, and both X and Y influence participation, then in the selected sample Gx will appear to be associated with Y (unless X is also controlled for).”

5. The paper’s guidance on what to adjust for (Abstract, final sentences):

   “Our results highlight the value of knowing which population your study sample is representative of. If the factors influencing selection and attrition are known, they can be adjusted for.”

6. When collider bias should be small (Box 3, “Does representativeness matter?”):

   “If the outcome of interest has not influenced selection into the intended study population, and all of this population is included in the study (i.e., in what we have described as the ‘actual study population’), then selection bias, and therefore collider bias, should be small.”

7. “Common effect” — the collider named as such (section “Collider bias”, ¶5):

   “If two traits influence participation (and therefore contribute to selection), selection bias amounts to implicitly conditioning on their common effect (i.e. participation).”

   (This is the only place the paper uses common-cause/common-effect vocabulary. It supplies the collider = common effect half. The confounder = common cause half is never stated — see §10.)

8. The intuition pump (Figure 1 caption):

   “In this example, a bell is sounded whenever either coin come up ‘heads’. The result of one coin toss is independent of the other. However, if we hear the bell ring (i.e. we condition on the bell ringing), then if we see a tail on one coin we know there must be a head on the other–the two coin results are no longer independent and a spurious inverse correlation has been induced.” (Figure 1 is reproduced by the authors from Gage SH, Davey Smith G, Ware JJ, Flint J, Munafò MR. G = E: What GWAS can tell us about the environment. PLoS Genet 2016;12:e1005765.)

8. Stated scope, assumptions, limitations (the source’s own caveats)

• Simulation assumptions are explicit and restrictive: all variables Normal with SD 1; P and O have independent (no additive-scale interaction) effects on odds of selection; those two effects are set equal “for convenience”; the analysis model is a plain unadjusted linear regression of outcome on allele score.
• The parametric model matters — there are exceptions. “There are exceptions to this, depending on the distribution of the outcome and the parametric analysis model used. For example, if the outcome (Y) is a binary phenotype, and logistic regression is used, then the odds ratio for the association between the single nucleotide polymorphism (SNP) and outcome may be unbiased even when the outcome causes selection (as is true of case-control studies)” (ref 15).
• Not exhaustive. “Other, more complex, situations can also lead to selection bias—we have not attempted to outline every possible case here.” The paper points to published algorithms for deciding whether a given causal analysis is biased by selection (ref 16, Daniel et al., Using causal diagrams to guide analysis in missing data problems) as the general tool.
• Remedies are conditional. Multiple imputation or inverse probability weighting can recover unbiased estimates only where some data are available on the missing individuals (e.g. drop-out), and even then only “under some assumptions which are untestable given the observed data” (ref 28). Where there is no information on the missing (e.g. never-volunteers), these methods cannot be used; only external information (e.g. known population sex ratio) offers a route to bias-adjusted estimates.
• For secondary-phenotype analysis in case-control studies, proposed fixes (maximum likelihood, inverse probability weighting) require knowing case/control prevalence in the intended study population, or assuming the disease is rare (refs 29, 30).
• The authors are revising their own prior position (refs 10, 12), which had held that selection bias would be modest for genetic associations; they do not claim their earlier reasoning was worthless, only that polygenic scores and highly selected samples change the calculus.
• Framed as opinion where it is opinion: “In our opinion these important caveats should be borne in mind when interpreting the results of such studies.”
• Box 3 concedes the biases in some cases “may be small in magnitude, but as we increasingly investigate small associations, their relative importance may be greater than is appreciated.”

9. Failure modes / invalidity patterns (referee-relevant)

When collider/selection bias occurs:

• Two variables (exposure and outcome, or their causal ancestors) independently cause a third variable, and analysis is restricted to (or adjusted for) that third variable. Study participation / retention / sub-study inclusion is such a third variable.
• Attrition as well as selection at inception — either alone, or both. A cohort can start representative and become unrepresentative through non-random drop-out (including drop-out by death).
• Sub-sampling within a study (e.g. selecting the people with the most complete data, or with DNA at multiple time points, for genotyping) is a second, often invisible, selection step — the ARIES example.
• Selection driven by only ONE of the two variables can still bias (Figure 3B): if entry depends on the phenotype but not the outcome, and P does not cause O but P and O are correlated in unselected samples via shared factors U, then conditioning on selection induces an association between SNPs for P and the factors influencing O — “SNPs that cause the phenotype only (i.e. do not in truth cause the outcome) may now show spurious relationships with the outcome variable.”
• Survival / mortality selection is the canonical instance of Figure 3B. Worked named example: smoking causes premature mortality; in a cohort followed for Alzheimer’s disease, those who die early “will never have the chance to be diagnosed with Alzheimer’s disease, and therefore smoking will appear to be a protective factor” (refs 32–35).
• Case-control secondary phenotypes: conditioning on case/control status when both genotype and the secondary phenotype relate to case status.
• Highest-risk analyses named: polygenic risk scores, genome-wide allelic scores (ref 20), whole-genome genetic correlations / LD-score-type genetic correlations (refs 21, 22) — because aggregation makes the score a stronger correlate of participation than any single variant.

Symptoms / detectors the paper names:

• Test whether measured variables predict participation/retention. The paper’s operational detector is exactly this: regress participation (or retention, or sub-study membership) on the phenotype, the outcome, and — critically — on a polygenic score (Box 1’s BMI/smoking→retention ORs; Table 3’s “association with being in the ARIES sub-study” panel). Non-null → selection is operating on that variable.
• Compare sample composition to the source population (UK Biobank Box 2: 11% vs 19% smokers, 17% vs 25% with no qualifications).
• Compare an association in the full cohort vs the selected sub-sample (Table 3: null in ALSPAC, significant in ARIES).
• Apparently paradoxical / direction-flipping / age- or threshold-dependent results are flagged as a signature worth suspecting: the schizophrenia-PRS threshold reversal (ref 27), the age-dependent genetic correlations (ref 26), protective-looking smoking effects.
• The algorithms of Daniel et al. (ref 16) are named as the formal check for whether a given causal analysis is biased by selection.

Where the bias does NOT bite / is small (the paper’s own negligibility conditions):

• Box 3 condition: if the outcome of interest has not influenced selection into the intended study population, and the whole intended study population is actually in the study, then selection bias — and therefore collider bias — should be small. (This is the paper’s only general negligibility statement.)
• Binary outcome + logistic regression: the SNP–outcome odds ratio “may be unbiased even when the outcome causes selection (as is true of case-control studies)” (ref 15).
• Figure 3 panel F: a structure where selection biases the P–O association but the SNP–O association remains unbiased in the selected sample.
• Empirically, from Table 1: at selection OR = 1.2 (a 0.2 SD shift between participants and non-participants) coverage stays near nominal (89–97 of 100 CIs contain zero) across all r; the damage becomes severe at OR = 1.8 and/or r ≥ 0.15.
• Adjustment is a remedy here, not the disease: “unless X is also controlled for” — controlling for the selecting phenotype blocks the induced Gx–Y association; and “If the factors influencing selection and attrition are known, they can be adjusted for.”

10. What the source does NOT address (confident silences)

Read carefully for each of these; each is a genuine silence, not an oversight in my reading.

• It never defines a confounder, and never draws an explicit confounder-vs-collider contrast. The word “confounding” appears in exactly two places, both in the same sense — “conventional confounding is [typically] low [for single genetic variants]” (Introduction, and again in the paragraph before Simulations) — used to explain why the authors had previously judged selection bias unimportant for genetic associations. It is never defined and never contrasted with a collider. The paper does supply the collider = common effect half of the contrast, in one sentence: selection bias “amounts to implicitly conditioning on their common effect (i.e. participation)” (§7 quote 7). But there is no sentence saying “a confounder is a common cause — adjust for it; a collider is a common effect — do not adjust for it.” The common-cause half is simply absent. Cite this paper for the collider/common-effect half only; do not cite it for the confounder side of that contrast, or for the adjust/don’t-adjust rule.
• It never discusses mediators as such, and never states the consequence of adjusting for a variable on the causal path. Causal chains do appear (Figure 3 C–E involve SNPs that “cause the outcome directly via the phenotype”; “unless X is also controlled for” is, structurally, adjusting for an intermediate), but the paper does not name mediation, does not warn against over-adjustment for mediators, and in fact only ever invokes controlling for X as a fix. Do not import the mediator case from this source.
• It never criticizes a “kitchen sink” / “adjust for everything measured” covariate strategy. No such statement exists. Its only adjustment guidance points the other way: adjust for the factors influencing selection, if you know them. (See §12 for the precise scope answer.)
• It gives no worked example, simulation, or empirical demonstration of adjusting for a measured collider covariate in a regression. Every simulation and every real-data example is about selection into a sample. The covariate-adjustment case is asserted in one sentence (§7 quote 1) and then immediately converted into the selection case.
• Batch effects, batch design, technical/laboratory covariates, and genomics assay batches are not mentioned at all. No occurrence of “batch” anywhere in the paper (except “UK BiLEVE” array selection, which is about which people were genotyped on which array, i.e. selection — not about batch as a technical confounder). Any transfer of this paper’s argument to batch-covariate selection or batch adjustment would be an external inference, not the source’s claim.
• No formal derivation. The bias is not derived algebraically; there is no closed-form expression for the magnitude of the induced association as a function of the selection ORs and r. The magnitude claims rest entirely on the 100-replicate simulations of Tables 1–2.
• No d-separation / back-door-criterion machinery. DAGs are used illustratively; the paper defers the formal decision procedure to ref 16 rather than presenting one.
• No treatment of population stratification, Mendelian randomization instrument validity, or linkage disequilibrium as such (allele scores are used purely as exposures/proxies here).
• No software, code, or package is provided or named for the simulations.

11. Open questions / ambiguities the source leaves unresolved

• Figure 3’s six panels (A–F) cannot be redrawn from the text. The prose describes A and B (SNP not causally associated with outcome; selection induces an association), C and D (SNP causally associated; selection could inflate or attenuate), E (SNP causally associated; selection biases the association either way), and F (P–O biased but SNP–O unbiased), and the caption names the node set P (phenotype), O (outcome), S (selection), U (other variables) — but the arrow directions that distinguish A from B, or C from D, live in the image. To reconstruct them the figure image must be consulted. The one structure the prose does pin down is panel B: selection depends on P but not on O; P does not cause O; P and O are correlated via shared genetic/environmental factors U.
• How large is the bias relative to a real effect, in general? The paper only shows two settings (true effect 0 and true P→O effect 0.1) with equal selection ORs for P and O. Unequal selection effects, interactions on the additive scale, non-Normal variables, and binary exposures are all left unexplored.
• What to do when selection factors are unknown is left largely open: the abstract’s proposal is to genotype everyone at recruitment so that polygenic prediction of subsequent participation can be estimated and used in sensitivity analyses — a suggestion, not a demonstrated method. No sensitivity-analysis procedure is specified or evaluated in this paper.
• Whether the reported real-world associations it names (personality↔cognition, chronotype↔ education) actually ARE collider artefacts is not settled — the claim is only that they “could therefore plausibly be generated by selection bias.”
• The paper says the outcome distribution and analysis model determine whether bias arises (the logistic/binary exception) but does not map out which model–distribution combinations are safe.

12. Guidance answers

The scope question (asked explicitly, answered precisely)

Q: Is this paper framed around selection bias / selection into a sample, or around covariate adjustment generally?

A: It is framed around SELECTION BIAS — selection into, and attrition from, a study sample. Not around covariate adjustment generally. This is not a close call:

• The title, abstract, and keywords (“Collider bias, selection bias, representativeness, cohort studies, UK Biobank, ALSPAC”) are all about selection.
• The stated research question is “what is the impact of selection bias on the results obtained from these studies?”, and the paper’s contribution is the perspective that selection bias “amounts to conditioning on a collider.”
• Every simulation and every empirical example conditions on participation (UK Biobank response, ALSPAC retention, ARIES sub-study membership, case-control status), never on a measured covariate in a regression.
• The paper’s closing framing is about representativeness of cohorts and knowing the selection mechanism.

However — and this is the load-bearing nuance — the paper DOES state the general covariate-adjustment mechanism, in one sentence, and uses it as the bridge to selection: “statistical adjustment for Z will bias the estimated causal association of X (exposure) on Y (outcome)”, justified by “Statistical adjustment of the XY association for a variable Z is equivalent to observing this association in a sub-population where all individuals share the same value of Z” (§7 quote 1). So the paper asserts that adjusting for a collider covariate biases the X–Y association — and treats selection as a special case of that, not the other way round.

But it never develops, demonstrates, quantifies, or exemplifies the covariate-adjustment case. There is no worked example, no simulation, and no empirical result in this paper in which a researcher adjusts a regression for a measured collider covariate. The whole apparatus — Tables 1–3, Figures 2 and 3, Boxes 1–3 — is selection.

Practical bound for citing it: this paper is a sound primary citation for (a) the definition of a collider as a common effect, (b) the claim that conditioning on / adjusting for a collider induces a spurious association, (c) the equivalence of adjustment and sub-population restriction, and (d) the magnitude of collider bias in the selection setting, with real parameters. It is not a citation for how bad it is to throw a measured collider into a regression’s covariate list (the quantitative claims are all selection-parameterized), and it is not a citation for the confounder-vs-collider adjust/don’t-adjust rule, which it never states. The guidance file’s suggested deeper primary (Greenland, Pearl & Robins 1999, Epidemiology 10:37–48) is indeed not superseded by this paper; a nearer, open-access alternative the paper itself cites for the general adjustment case is Elwert & Winship 2014, “Endogenous selection bias: the problem of conditioning on a collider variable,” Annu Rev Sociol 40:31–53 (ref 31) and Hernán, Hernández-Díaz & Robins, “A structural approach to selection bias,” Epidemiology 2004;15:615–25 (ref 13).

Point-by-point against the guidance file

Must capture — the mechanism

Must capture — magnitude

Must-quote items

Silences to record explicitly

Pin

DOI 10.1093/ije/dyx206; Int J Epidemiol 47(1):226–235 (2018); PMID 29040562; PMCID PMC5837306. Read from the PMC full-text deposit; accessed 2026-07-13. License CC-BY-4.0 (explicit statement on the article; see §1) → license-aware summary, verbatim quotes permitted and marked.